2. Subclassification STA 320 Design and Analysis of Causal Studies Dr. Kari Lock Morgan and Dr. Fan Li Department of Statistical Science Duke University

3. Quiz 2 > summary(Quiz2) Min. 1st Qu. Median Mean 3rd Qu. Max. 11.0 14.0 15.0 15.5 17.0 20.0

4. Quiz 2 one-sided or two-sided p-value? (depends on question being asked) imputation: use observed control outcomes to impute missing treatment outcomes and vice versa. o class year: use observed outcomes from control sophomores to impute missing outcomes for treatment sophomores biased or unbiased

5. Covariate Balance In randomized experiments, the randomization creates covariate balance between treatment groups In observational studies, treatment groups will be naturally unbalanced regarding covariates Solution? compare similar units (How? Propensity score methods.)

6. Shadish Covariate Balance GOAL THIS WEEK: Try to fix this!

7. Select Facts about Classical Randomized Experiments Timing of treatment assignment clear Design and Analysis separate by definition: design automatically “prospective,” without outcome data Unconfoundedness, probabilisticness by definition Assignment mechanism – and so propensity scores – known Randomization of treatment assignment leads to expected balance on covariates (“Expected Balance” means that the joint distribution of covariates is the same in the active treatment and control groups, on average) Analysis defined by protocol rather than exploration 6 Slide by Cassandra Pattanayak

8. Select Facts about Observational Studies Timing of treatment assignment may not be specified Separation between design and analysis may become obscured, if covariates and outcomes arrive in one data set Unconfoundedness, probabilisticness not guaranteed Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 7 Slide by Cassandra Pattanayak

9. Best Practices for Observational Studies Timing of treatment assignment may not be specified Separation between design and analysis may become obscured, if covariates and outcomes arrive in one data set Unconfoundedness, probabilisticness not guaranteed Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 8 Slide by Cassandra Pattanayak

10. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables Separation between design and analysis may become obscured, if covariates and outcomes arrive in one data set Unconfoundedness, probabilisticness not guaranteed Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 9 Slide by Cassandra Pattanayak

11. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete Unconfoundedness, probabilisticness not guaranteed Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 10 Slide by Cassandra Pattanayak

12. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 11 Slide by Cassandra Pattanayak

13. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group Assignment mechanism – and therefore propensity scores – unknown Lack of randomization of treatment assignment leads to imbalances on covariates Analysis often exploratory rather than defined by protocol 12 Slide by Cassandra Pattanayak

14. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group 5. Estimate propensity scores, as a way to… 6. Find subgroups (subclasses or pairs) in which the active treatment and control groups are balanced on covariates (not always possible; inferences limited to subgroups where balance is achieved) Analysis often exploratory rather than defined by protocol 13 Slide by Cassandra Pattanayak

15. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group 5. Estimate propensity scores, as a way to… 6. Find subgroups (subclasses or pairs) in which the treatment groups are balanced on covariates (not always possible; inferences limited to subgroups where balance is achieved) Analysis often exploratory rather than defined by protocol 14 Slide by Cassandra Pattanayak

16. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group 5. Estimate propensity scores, as a way to… 6. Find subgroups (subclasses or pairs) in which the active treatment and control groups are balanced on covariates (not always possible; inferences limited to subgroups where balance is achieved) 7. Analyze according to pre-specified protocol 15 Slide by Cassandra Pattanayak

17. Best Practices for Observational Studies 1. Determine timing of treatment assignment relative to measured variables 2. Hide outcome data until design phase is complete 3. Identify key covariates likely related to outcomes and/or treatment assignment. If key covariates not observed or very noisy, usually better to give up and find a better data source. 4. Remove units not similar to any units in opposite treatment group 5. Estimate propensity scores, as a way to… 6. Find subgroups (subclasses or pairs) in which the active treatment and control groups are balanced on covariates (not always possible; inferences limited to subgroups where balance is achieved) 7. Analyze according to pre-specified protocol 16 Design Observational Study to Approximate Hypothetical, Parallel Randomized Experiment Slide by Cassandra Pattanayak

18. Propensity Scores ps = predict(ps.model, type="response")

19. Trimming Eliminate cases without comparable units in the opposite group One option: set boundaries on the allowable propensity score and eliminate units with propensity scores close to 0 or 1 Another option: eliminate all controls with propensity scores below the lowest treated unit, and eliminate all treated units with propensity scores above the highest control

20. Trimming No comparable treated units - eliminate these control units ps = predict(ps.model, type="response")

21. Trimming > overlap(ps, data$W) #these units should be eliminated [1] “8 controls below any treated" [1] “5 treated above any controls” > data = data[ps>=min(ps[data$W==1]) & ps <= max(ps[data$W==0]),]

22. Estimating Propensity Scores In practice, estimating the propensity score is an iterative process: 1.Estimate propensity score 2.Eliminate units with no overlap (eliminate units with no comparable units in other groups) 3.Repeat until propensity scores overlapping everywhere for both groups Go back and refit model

23. New Propensity Scores trim non-overlap… refit propensity score model…

24. New Propensity Scores

25. After Trimming: Love Plot Original n = 210; after trimming n = 187 the closer to 0, the better! (0 = perfect balance) Before trimming After trimming

26. Love Plots The previous plot is called a love plot (Thomas Love): used to visualize improvement in balance Original statistics are t-statistics Statistics after balancing use the same denominators (SE) as the original t-statistics o Otherwise closer to 0 could be from increased SE o No longer t-statistics, just for comparison o Only numerators (difference in means) change o If smaller, must be better balance

27. Trimming Trimming can improve covariate balance, improving internal validity (better causal effects for remaining units) But hurts external validity (generalizability) Changes the estimand – estimate the causal effect for those units who are comparable How many units to trim is a tradeoff between decreasing sample size and better comparisons – Ch 16 gives optimal threshold

28. Subclasses If we have enough covariates (unconfounded), within subclasses of people with identical covariates, observational studies look like randomized experiments Idea: subclassify people based on similar covariate values, and estimate treatment effect within each subclass (similar to stratified experiments)

29. One Key Covariate Smoking, Cochran (1968) Population: Male smokers in U.S. Active treatment: Cigar/pipe smoking Control treatment: Cigarette smoking Outcome: Death in a given year Decision-Maker: Individual male smoker Reason for smoking male to choose cigarettes versus cigar/pipe? Age is a key covariate for selection of smoking type for males 28 Slide by Cassandra Pattanayak

30. Subclassification to Balance Age To achieve balance on age, compare: - “young” cigar/pipe smokers with “young” cigarette smokers - “old” cigar/pipe smokers with “old” cigarette smokers Better: young, middle-aged, old, or more age subclasses Objective of study design, without access to outcome data: approximate a completely randomized experiment within each subclass Only after finalizing design, reveal outcome data 29 Rubin DB. The Design Versus the Analysis of Observational Studies for Causal Effects: Parallels with the Design of Randomized Trials. Statistics in Medicine, 2007. Slide by Cassandra Pattanayak

31. Comparison of Mortality Rates for Two Smoking Treatments in U.S. 30 Cochran WG. The Effectiveness of Adjustment of Subclassification in Removing Bias in Observational Studies. Biometrics 1968; 24: 295-313. Cigarette Smokers Cigar/Pipe Smokers Mortality Rate per 1000 person-years, % 13.517.4 Slide by Cassandra Pattanayak

32. Comparison of Mortality Rates for Two Smoking Treatments in U.S. 31 Cochran WG. The Effectiveness of Adjustment of Subclassification in Removing Bias in Observational Studies. Biometrics 1968; 24: 295-313. Cigarette Smokers Cigar/Pipe Smokers Mortality Rate per 1000 person-years, % 13.517.4 Averaging Over Age Subclasses 2 Age Subclasses16.414.9 3 Age Subclasses17.714.2 11 Age Subclasses21.213.7 Slide by Cassandra Pattanayak

33. What if we had 20 covariates, with 4 levels each? Over a million million subclasses 32 Slide by Cassandra Pattanayak

34. Solution? How can we balance many covariates? BALANCE THE PROPENSITY SCORE!

35. Propensity Score Amazing fact: balancing on just the propensity score balances ALL COVARIATES included in the propensity score model!!!

36. Toy Example One covariate, X, which takes levels A, B, C X = AX = BX = C Treatmen t 9025 Control10820 e(x)0.90.2 Within circled subclass, are treatment and control balanced with regard to X? Yes! Each has 2/7 B and 5/7 C

37. Hypothetical Example Population: 2000 patients whose medical information was reported to government database Units: Patients Active Treatment: New surgery (1000 patients) Control Treatment: Old surgery (1000 patients) Outcome: Survival at 3 years Remove outcomes from data set 36 Slide by Cassandra Pattanayak

38. Reasonable to assume propensity score = 0.5 for all? 37 Age RangeTotal NumberNumber New Surgery Number Old Surgery Estimated Probability New Surgery, given Age 0-19137944394/137 = 0.69 20-39455276179276/455 = 0.61 40-59790393397393/790 = 0.50 60-79479193286193/479 = 0.28 80-99118318731/118 = 0.26 Slide by Cassandra Pattanayak

39. Does propensity score depend on age only? 38 Cholesterol Range Total NumberNumber New Surgery Number Old Surgery Estimated Probability New Surgery, given Cholesterol 0-19917515520155/175 = 0.89 200-249475354121354/475 = 0.75 250-299704343361343/704 = 0.49 300-349464130334130/464 = 0.28 350-4001621614616/162 = 0.10 Slide by Cassandra Pattanayak

40. 39 Age Cholesterol 0-1920-3940-5960-7980-99 0-19911/11 1.00 32/38 0.84 32/49 0.65 17/29 0.59 2/7 0.29 200-24957/61 0.93 100/119 0.84 75/141 0.53 40/103 0.39 4/25 0.16 250-29948/57 0.84 145/191 0.76 148/293 0.51 43/177 0.24 7/67 0.10 300-34928/33 0.85 63/98 0.64 72/172 0.42 28/125 0.22 2/46 0.04 350-4009/10 0.90 8/22 0.36 11/43 0.26 2/28 0.07 1/13 0.08 Proportion of units assigned to active treatment rather than control treatment Slide by Cassandra Pattanayak

41. Age Cholesterol 0-1920-3940-5960-7980-99 0-19911/11 1.00 32/38 0.84 32/49 0.65 17/29 0.59 2/7 0.29 200-24957/61 0.93 100/119 0.84 75/141 0.53 40/103 0.39 4/25 0.16 250-29948/57 0.84 145/191 0.76 148/293 0.51 43/177 0.24 7/67 0.10 300-34928/33 0.85 63/98 0.64 72/172 0.42 28/125 0.22 2/46 0.04 350-4009/10 0.90 8/22 0.36 11/43 0.26 2/28 0.07 1/13 0.08 Proportion of units assigned to active treatment rather than control treatment Slide by Cassandra Pattanayak

42. Age Cholesterol 0-1920-3940-5960-7980-99 0-19911/11 1.00 32/38 0.84 200-24957/61 0.93 100/119 0.84 250-29948/57 0.84 145/191 0.76 300-34928/33 0.85 350-4009/10 0.90 Subclassifying on estimated propensity score leads to active treatment and control groups, within each subclass, that have similar covariate distributions Slide by Cassandra Pattanayak

43. Age Cholesterol 0-1920-3940-5960-7980-99 0-1991132 200-24957100 250-29948145 300-34928 350-4009 Number of active treatment units, subclass 1 Slide by Cassandra Pattanayak

44. Age Cholesterol 0-1920-3940-5960-7980-99 0-19911/430 0.03 32/430 0.07 200-24957/430 0.13 100/430 0.23 250-29948/430 0.11 145/430 0.34 300-34928/430 0.07 350-4009/430 0.02 Covariate distribution among active treatment units, subclass 1 Slide by Cassandra Pattanayak

45. Age Cholesterol 0-1920-3940-5960-7980-99 0-19911/11 1.00 32/38 0.84 200-24957/61 0.93 100/119 0.84 250-29948/57 0.84 145/191 0.76 300-34928/33 0.85 350-4009/10 0.90 Proportion of units assigned to active treatment rather than control treatment Slide by Cassandra Pattanayak

46. Age Cholesterol 0-1920-3940-5960-7980-99 0-19906 200-249419 250-299946 300-3495 350-4001 Number of control treatment units, subclass 1 Slide by Cassandra Pattanayak

47. Age Cholesterol 0-1920-3940-5960-7980-99 0-1990/90 0.00 6/90 0.07 200-2494/90 0.04 19/90 0.21 250-2999/90 0.10 46/90 0.51 300-3495/90 0.06 350-4001/90 0.01 Covariate distribution among control treatment units, subclass 1 Slide by Cassandra Pattanayak

48. Age Cholesterol 0-1920-39 0-19911/430 0.03 32/430 0.07 200-24957/430 0.13 100/430 0.23 250-29948/430 0.11 145/430 0.34 300-34928/430 0.07 350-4009/430 0.02 Covariate distribution among active treatment units, subclass 1 Age Cholesterol 0-1920-39 0-1990/90 0.00 6/90 0.07 200-2494/90 0.04 19/90 0.21 250-2999/90 0.10 46/90 0.51 300-3495/90 0.06 350-4001/90 0.01 Covariate distribution among control treatment units, subclass 1 Slide by Cassandra Pattanayak

49. Stratified randomized experiment: - Create strata based on covariates - Assign different propensity score to each stratum - Units with similar covariates are in same stratum and have same propensity scores Observational study: - Estimate propensity scores based on covariates - Create subclasses based on estimated propensity scores - Units within each subclass have similar propensity scores and, on average, similar covariates Works if we have all the important covariates – i.e., if assignment mechanism unconfounded given observed covariates 48 Slide by Cassandra Pattanayak

50. Subclassification Divide units into subclasses within which the propensity scores are relatively similar Estimate causal effects within each subclass Average these estimates across subclasses (weighted by subclass size) (analyze as a stratified experiment)

51. Estimate within Subclass If propensity scores constant enough within subclass, often a simple difference in observed means is adequate as an estimate If covariate differences between treatment groups persist, even within subclasses, regression or model-based imputation may be used

52. How many subclasses? It depends! (covariate balance, n, etc.) More subclasses: propensity scores will be closer to the same within each subclass Fewer subclasses: sample sizes will be larger within each subclass, so estimates will be less variable Larger sample size can support more subclasses

53. How many subclasses? Start with 5 equally sized subclasses (usually 5-10 are sufficient) Check… o Propensity score balance within subclasses o Number of treated and controls within subclasses o Overall covariate balance If balance needs improving and subclasses have enough treated and controls, try more subclasses

54. Subclass Breaks Starting with 5 equally sized subclasses Subclass breaks would be at the 20 th, 40 th, 60 th, and 80 th percentiles of the propensity score Subclasses do not have to be equally sized, that’s just a convenient starting point

55. Shadish Data > subclass.breaks = quantile(ps, c(.2,.4,.6,.8)) > subclass = subclasses(ps, subclass.breaks) > plot.ps(ps, W, subclass.breaks)

56. Shadish Data > table(W, subclass) subclass W 1 2 3 4 5 0 19 18 12 7 7 1 19 19 25 30 31

57. Love Plot > cov.balance(X, W) > cov.balance(X, W, subclass) Raw Subclassified

58. Outcomes Once we are happy with the covariate balance, we can analyze the outcomes (Note: once you look at the outcomes, there is no turning back, so make sure you are happy with balance first!)

59. Inference: Estimate Analyze as a stratified experiment General (where j indexes subclasses): One common option:

60. Shadish Data: Outcomes! > subclass.average(MathOutcome, W, subclass) $`Difference in Means within Each Subclass` [1] -1.263158 -4.681287 -4.016667 -6.633333 -3.658986 $`Weighted Average Difference in Means` [,1] [1,] -4.033685 > subclass.average(VocabOutcome, W, subclass) $`Difference in Means within Each Subclass` [1] 9.000000 9.289474 7.856667 5.828571 8.626728 $`Weighted Average Difference in Means` [,1] [1,] 8.127701 Taking the vocab training rather than the math training course causes a decrease of about 4 points on the math test and an increase of about 8 points on the vocab test, on average.

61. Shadish Data n = 445 undergraduate students Randomized Experiment 235 Observational Study 210 Vocab Training 116 Math Training 119 Vocab Training 131 Math Training 79 randomization students choose Shadish, M. R., Clark, M. H., Steiner, P. M. (2008). Can nonrandomized experiments yield accurate answers? A randomized experiment comparing random and nonrandom assignments. JASA. 103(484): 1334-1344.

62. Shadish Data: Outcomes! > subclass.average(MathOutcome, W, subclass) $`Difference in Means within Each Subclass` [1] -1.263158 -4.681287 -4.016667 -6.633333 -3.658986 $`Weighted Average Difference in Means` [,1] [1,] -4.033685 > subclass.average(VocabOutcome, W, subclass) $`Difference in Means within Each Subclass` [1] 9.000000 9.289474 7.856667 5.828571 8.626728 $`Weighted Average Difference in Means` [,1] [1,] 8.127701 Taking the vocab training rather than the math training course causes a decrease of about 4 points on the math test and an increase of about 8 points on the vocab test. Estimate from randomized experiment: -4.189 Estimate from randomized experiment: 8.114

63. Inference: Variance General (where j indexes subclasses): If using simple difference in means:

64. Shadish Data: Inference > subclass.var(MathOutcome, W, subclass) $`Variance within Subclasses` [1] 1.859820 1.627395 1.617101 1.946617 4.144487 $`Variance of Estimate` [,1] [1,] 0.2856831 $`SE of Estimate` [,1] [1,] 0.5344934 > subclass.var(VocabOutcome, W, subclass) $`Variance within Subclasses` [1] 2.853668 3.198244 3.209063 7.074847 7.376476 $`Variance of Estimate` [,1] [1,] 0.6017093 $`SE of Estimate` [,1] [1,] 0.7756993

65. Shadish Data: Math We are 95% confident that taking the math training course (as opposed to the vocab course) increases math scores by between about 3 and 5 points, on average. This is highly significant – taking the math course does improve your math test score.

66. To Do Read Ch 16, 17 Homework 4 (due Monday) Bring laptops to class on Wednesday